Design-Based Inference

• Contrast to conditioning
• Difference-in-Differences
• Natural Experiments

Design vs. Model-based inferences

A matter of degree

Statistical evidence for causality combines observed data with a mathematical model of the world

• mathematical model describes how observed data are generated
• model always involves assumptions
• can almost always apply the model, even if it is wrong

Design vs. Model-based inferences

Causal evidence varies in terms of complexity of math/assumptions: a matter of degree

• Model-based inferences about causality depend on complex statistical models with many assumptions

• Design-based inferences about causality use carefully controlled comparisons with simple, transparent models and assumptions

Design vs. Model-based inferences

Whatever our approach…

do the assumptions needed to use this mathematical tool reasonably fit reality?

Conditioning vs. Design

When we condition, we block specific backdoor paths that generate confounding by comparing cases that are similar on observable trait:

• we must assume that treatment is conditionally independent on these traits, that there is positivity, and that there is no measurement error.
• we did exact matching last week, but most conditioning strategies involve additional modelling assumptions to be tractable

Conditioning vs. Design

In the absence of an experiment, we might choose more careful research designs, instead of relying on conditioning.

• comparing the same unit over time
• differences-in-differences
• “natural” experiments:
  • sources of “randomness” in the world
  • arbitrary thresholds

Here, the structure of the comparison motivates an argument for independence of cause and potential outcomes. Rather than block specific confounding variables, we eliminate confounding due to a class of confounding variables.

Media Effects on Political Attitudes

Social and political theorists have frequently argued that media—by shaping perceptions of events in the world, exposing people to narrative frames—affects beliefs and behaviors.

• What might be some obstacles to evaluating the causal effect of media exposure?
• Why might experiments be a poor strategy?
• Why might conditioning not work very well?

Media Effects

Foos and Bischoff examine the effect of changing exposure to The Sun on anti-EU attitudes and voting in the UK.

• The Sun is a tabloid with long-standing anti-EU coverage and editorial slant
• In 1989, ~100 fans of Liverpool FC died in stampede at a match; The Sun blamed the victims for the tragedy
• Boycott of the The Sun by fans and teams in the Liverpool area.

Conditioning?

We could ignore this shift, and simply compare attitudes about the EU in areas (or among people) with greater vs less readership of The Sun:

• What might be some reasons to doubt the effectiveness of this approach?

Interrupted Time Series

We could instead, compare attitudes toward the EU in Liverpool before and after the boycott:

• What might some advantages of this be?

• Block all confounding variables that remain constant over time within Liverpool
• Advantage: No need to know what these variables are, measure them, specify a model, etc.

Interrupted Time Series

In interrupted time series, we plug in the observed outcome before treatment for the counterfactual outcome where treatment did not happen: where \(t=1\) indicates post-treatment, \(t=0\) indicates before treatment.

\[\tau_i = [Y_{i,t=1}(1) | D_i = 1] - \color{red}{[Y_{i,t=1}(0)|D_i = 1]}\]

Plugging in:

\[\widehat{\tau_i} = [Y_{i,t=1}(1) | D_i = 1] - [Y_{i,t=0}(0) | D_i = 1]\]

What can go wrong here?

Interrupted Time Series

In order for interrupted time series to work, we must assume:

\[[Y_{i,t=0}(0) | D_i = 1] = \color{red}{[Y_{i,t=1}(0)|D_i = 1]}\]

That in the absence of the treatment, outcomes of \(Y\) would not have changed from before to after treatment.

• Why might this be incorrect in general? In the context of the Liverpool Sun boycott?

Interrupted Time Series

Assumptions mean: none of the following

• “history”: bias related to other changes year-to-year changes (short-term trends)
• “maturation”: bias / confounding due to long-term trends
• “testing”: bias /confounding related to selection into “treatment” (what kinds of things led to the policy adoption)
• “regression”: cases select into treatment due to extreme events, followed by return to the norm
• “instrumentation”: treatment induces change in measurement (non-random measurement error)

Interrupted Time Series

A good example:

Mummolo 2018

Difference-in-Differences:

Difference-in-differences compares changes in the treated cases against changes in untreated cases.

Again, we want to know:

\[\begin{split}E[\tau_i | D_i = 1] = {} \frac{1}{n}\sum\limits^{n}_{i=1} & [Y_{i,t=1}(1) | D_i = 1] - \\ & \color{red}{[Y_{i,t=1}(0)|D_i = 1]}\end{split}\]

• Is this the average causal effect?

Difference-in-Differences:

Interrupted Time Series forced us to assume no other changes in outcomes over time, but it is almost always true that:

\(\color{red}{Y_{i,t=1}(0) | D_i = 1]} - [Y_{i,t=0}(0)|D_i = 1] \neq 0\)

That is to say, counterfactually, in the absence of treatment \(D\), potential outcomes \(Y_i(0)\) are changing over time.Observed pre-treatment outcomes not a good substitute for post-treatment counterfactual outcomes.

• Do we have a way to estimate what these counterfactual trends absent treatment might be?

Difference-in-Differences:

We don’t know: \(\color{red}{Y_{i,t=1}(0) | D_i = 1]} - [Y_{i,t=0}(0)|D_i = 1]\)

But we do know: \(Y_{i,t=1}(0) | D_i = 0] - [Y_{i,t=0}(0)|D_i = 0]\)

In our example: we don’t know how EU skepticism might have trended in Liverpool absent the boycott. But we do know how EU skepticism in the rest of the UK trended absent the boycott.

Difference-in-Differences:

If we assume:

\[\{\overbrace{\color{red}{Y_{i,t=1}(0) | D_i = 1]} - [Y_{i,t=0}(0)|D_i = 1]}^{\text{Treated counterfactual trend}}\} = \\ \{\underbrace{Y_{i,t=1}(0) | D_i = 0] - [Y_{i,t=0}(0)|D_i = 0]}_{\text{Untreated observed trend}}\}\]

Then we can plug-in the \(observed\) untreated group trend for the \(\color{red}{counterfactual}\) treated group trend.

Difference-in-Differences:

This is the parallel trends assumption. It is equivalent to saying there are no time-varying confounding variables that differ between treated and untreated.

If it is true, we can do some simple algebra and find that

\([\tau_i | D_i = 1] = [Y_{i,t=1}(1) | D_i = 1] - \color{red}{[Y_{i,t=1}(0)|D_i = 1]}\)

\(\begin{equation}\begin{split}[\tau_i | D_i = 1] = {} & \{\overbrace{[Y_{i,t=1}(1) | D_i = 1] - [Y_{i,t=0}(0) | D_i = 1]}^{\text{Treated observed trend}}\} - \\ & \{\underbrace{\color{red}{Y_{i,t=1}(0) | D_i = 1]} - [Y_{i,t=0}(0)|D_i = 1]}_{\text{Treated counterfactual trend}}\}\end{split}\end{equation}\)

\(\begin{equation}\begin{split}[\widehat{\tau_i} | D_i = 1] = {} & \{\overbrace{[Y_{i,t=1}(1) | D_i = 1] - [Y_{i,t=0}(0) | D_i = 1]}^{\text{Treated observed trend}}\} - \\ & \{\underbrace{Y_{i,t=1}(0) | D_i = 0] - [Y_{i,t=0}(0)|D_i = 0]}_{\text{Untreated observed trend}}\}\end{split}\end{equation}\)

And this gives us the name:

• \(Treated_{post} - Treated_{pre}\) (first difference)
• \(Untreated_{post} - Untreated_{pre}\) (first difference)
• \((Treated_{post} - Treated_{pre}) - \\ (Untreated_{post} - Untreated_{pre})\)

• Difference in differences

Difference-in-differences:

This shows that the Boycott of the Sun reduced Euro Skepticism in Liverpool

• Under the parallel trends assumption (untreated cases have the same trends as treated cases in the absence of treatment)

• This is an unbiased estimate of the Average Treatment on Treated (\(ATT\)):

  • the effect of treatment on the treated cases
  • it is TOTALLY fine if the effect of treatment on untreated cases would be different

Difference-in-differences:

If parallel trends assumption holds, what kinds of confounding does this design eliminate?

• Any time-invariant confounders within units
• Any time-varying confounders that are shared by both treated cases and un-treated cases >- Crucial to choose right “control” cases to have parallel trends or e.g. share as many time-varying confounders.

What are examples of confounders held constant in Sun Boycott difference in difference?

Difference-in-differences:

Estimation:

• Classical scenario: with two “treatment” conditions, two time periods: calculate differences-in-differences in means
• We can use regression, dummy for ever-treated, dummy for post-treatment, interaction of the two

Difference-in-differences:

How do we validate the parallel trends assumption?

• We cannot directly test it, but we can try to see if it is plausible

Placebo Tests:

• If “treatment” happens between time \(t\) and \(t+1\), we should not see an effect between \(t-1\) and \(t\)!
• If design is right, there should be no effects of the treatment prior to the treatment taking place.
• If we “pass” placebo test, does not reject possibility that something other than “treatment” caused a change.
• You need multiple pre-treatment data points

Difference-in-differences: Extensions

Staggered Treatment: Bacon-Goodman 2021

Multiple Treatments: https://arxiv.org/pdf/1803.08807.pdf

Continuous Treatment: https://psantanna.com/files/Callaway_Goodman-Bacon_SantAnna_2021.pdf

As we get away from simple DiD, assumptions and potential problems multiply, solutions get more complicated…

An Example:

What was the effect of enlistment in the US Civil War on voting for the Republican party?

\(GOP_{ie} = \alpha_i + \alpha_e + \beta Enlist_i \times PostWar_e + \epsilon_y + \epsilon_i\)

• \(i\) is a county
• \(e\) is a state-election (election year in a specific state)
• \(y\) is a year between 1854 and 1880
• \(PostWar\) indicates if election is after 1861 \((1)\) or before \((0)\)

An Example:

An Example:

Difference-in-differences:

Assumptions:

• parallel trends: treated and untreated have same changes over time except for shift in treatment.
• equivalently: no time-varying omitted variable bias; no omitted variables correlated with changes in treatment, changes in outcome

Caveats:

• ‘check’ parallel trends
• careful: what happens when units are treated at different times? different amounts?
• careful: STANDARD ERRORS! Clustering may not save you with small \(N\).

Natural Experiments:

Address confounding in a different way:

• exploit random or as-if random allocation of \(X\) to find causal effect
• look for “naturally” occurring randomization

Natural Experiments:

Distinguishing “natural experiment” from experiments:

• Treatment and control groups
• Random assignment (maybe)
• “as-if” random assigment
• we don’t do the manipulation

Natural Experiments:

An observational study where causal inference comes from the design that draws on randomization.

• contrast to difference-in-differences
• depends on argument to validate “as-if” random assumption \(\to\) fewer assumptions in the statistical model

Regression Discontinuity

• “Treatment” occurs for cases on one side of threshold, not to cases on other side
• “Near” the hreshold, cases are effectively arbitrarily assigned.
  • treatment can be for ALL cases on the “Treated” side (sharp RD)
  • treatment can increase at the threshold (“fuzzy” RD) (e.g. Mo 2018)

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Regression Discontinuity

Two approaches:

• Potential outcomes of \(Y\) are approximately linear near the threshold; treatment shifts outcomes
  • so we (flexibly) model \(Y\) on either side of the cut-off
• Potential outcomes of \(Y\) are random near the cut-off
  • difference in means near the cutoff

Regression Discontinuity

Decisions:

• model outcome around cutoff
  • bias/variance trade-off
  • how do you model it? linear? quadratic? cubic? quartic? local linear?
  • how do you choose the “bandwidth” around the cutoff to use?
  • typically recommend local linear, automatic choice of ‘optimal bandwidth’
• difference in means at cutoff
  • how do you choose the “bandwidth” around the cutoff to use?

Regression Discontinuity

Assumptions:

• assignment to treatment at the threshold is random
• AND
  • either we have correctly modeled potential outcomes of \(Y\) on either side of cutoff
  • or we have used “bandwidth” around cutoff within which treatment is as-if random assigned (difference in means)

Instrumental Variables

Follows from Wald estimator for non-compliance:

• Instrumental Variables Least Squares uses variance “explained” in \(D\) by randomly induced \(Z\)
  • \(D\) is “treatment”, \(Z\) is “random assignment to treatment”
  • easy to understand when \(Z\) is binary
  • when \(Z\) is continuous, it is more complicated (and depends on assumptions of linearity)

Instrumental Variables

Decisions

• is variation induced in \(D\) by \(Z\) linear?
• does \(Z\) actually predict change in \(D\)?
  • “weak instruments problem”: identical to when there are very few compliers in an experiment: inference becomes very hard
  • typically do \(F\) test of regression of \(Y\) on \(X\); \(F\) statistic \(> 50\).

Instrumental Variables

Assumptions:

1. \(Z\) is randomly assigned
2. Exclusion Restriction
   • no other causal path from \(Z\) to \(Y\), other than \(X\)
3. Monotonicity
   • increasing \(Z\) uniformly increases or decreases values of \(X\)

Natural Experiments: Choices

• Sometimes natural experiments only random conditional on some other variables (Nellis, et al.)
  • What is the correct functional form for the conditioning variables?
• Standard Errors:
  • What is the unit at which treatment is assigned?
  • Cluster/Randomization inference

Natural Experiments: Limitations

• Effects are “local” or for “compliers”
• Effects for sub-group with randomization
  • like in non-compliance, we find subset of cases that are randomly induced into treatment/responsive
  • cases may be different from population of interest
• Causal exposures may be different
  • cause applied at cutoff might be different than elsewhere
  • cause applied at random might be different (e.g. rainfall as instrument for economic growth)

Natural Experiments: What to do

• Evidence that randomization took place
  • statistical tests of implication
  • qualitative evidence: “causal process observation”
• Show robustness to choices of analysis